Seventy days passed since the blog was open and I am glad to see that the first post received some 3000 visits and 20 comments, and the site received 22 user registrations. This is a clear indication that the discussion on the next IAHS scientific decade is relevant for the international community of hydrologists. I would like to draw a first summary of the discussion and to put forward more advanced ideas for setting up the basis of the next IAHS initiative.
Basically, the discussion so far has highlighted that:
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The new Science Initiative should be a substantial contribution to IAHS community building, should be inclusive (Hilary McMillan) and the subject should be attractive for funding agencies (Bettina Schaefli). It should be a multidisciplinary effort (Fabrizio Fenicia, Stan Schymanski).
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Hydrological change and variability, and the interaction between hydrology and society, are topical issues that deserve to be focused on (myself, Hoshin Gupta, Stan Schymanski, Giuliano Di Baldassarre).
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Uncertainty should be a keyword for the new initiative, in an innovative manner with respect to the traditional paradigm that attempted to eliminate uncertainty in hydrology (Demetris Koutsoyiannis, Christian Stamm).
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Understanding past and present is a key issue to foresee what the future will be (Ciaran Harman). Comparative hydrology is an effective tool to this end (Ciaran Harman, Siva Sivapalan).
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Modern technologies offer unprecedented opportunities (Salvatore Grimaldi, Demetris Koutsoyiannis, David Post).
- The new initiative should effectively focus on unstudied areas of the world (Alberto Viglione et al.).
- The new initiative should provide a sound scientific basis for adaptive management of water resources under uncertainty (Christian Stamm).
I believe the above summary provides a very useful and detailed first picture of the expectation from the IAHS community. I would propose to postpone the discussion related to the name of the new Science Initiative. Ideas for name and acronym will be collected later on. With this post, I would like to discuss the main theme for the new Science Initiative that emerged from the blog comments so far, by also stimulating ourselves to gain a better insight into the above bullet points.
Indeed, hydrological change is recognised to be a topical issue for hydrologists. Understanding and modelling the behaviour of hydrological (uncertain) systems under changing conditions is a compelling necessity to cope with environmental and social evolution and to provide a satisfactory reply to applied engineering problems. I think there is no doubt that the above issue is involving and attracting a wide part of the IAHS community.
However, it is still unclear how change can be modelled besides the traditional “top down” scenario approach. This latter is carried out by identifying and calibrating hydrological models in current conditions and then running them with perturbed parameters or input data according to assumptions on changing forcing and/or dynamics. As a matter of fact, the top down approach has been used in several studies already. On the one hand, it provided useful results. On the other hand, it has proved to be affected by significant limitations due to limited credibility of current models under changing conditions, uncertainty in future scenarios and model parameters. The results so far obtained call for improved approaches to better understand the interaction between hydrological systems and changing socio-economic and environmental forcing, besides what perturbations in input data and parameters suggest.
The question, then, is: what would be an innovative blueprint to understanding and modelling of changing systems? Replying to the above question means to put the basis for a vision on the science plan we are looking for. I am putting some ideas forward, by taking inspiration from what colleagues wrote on the blog. I am looking forward to your follow up.
1) A necessary prerequisite to understand changing system is to improve our understanding of their dynamics, and their evolution, in the current and past situation. The keyword would be “historical hydrology” and “process hydrology”. This is a first milestone that is rooted in classical hydrology and allows us to set up a connection with the previous decades, and in particular PUB, whose success is unquestionable. Experimental activity is essential, as well as improved process-based and stochastic modelling (possibly integrated in an innovative framework). I think a key step is to better understand hydrologic variability and evolution, which is of course extremely important in the face of change. New ideas are needed to effectively integrate experimental and modelling activity therefore gaining new insights into hydrological modelling.
2) A second prerequisite, which is not disjointed by the first, is uncertainty and predictability. Uncertainty should not be viewed as just a mean to compensate limited understanding. In the innovative view we would like to promote uncertainty should be treated as an effect of indeterminacy. It is a behaviour of hydrological processes, due to the fact that in some instances processes evolve randomly. Evolution itself, in biology, includes random processes (see http://en.wikipedia.org/wiki/Evolution), meaning that Nature evolves accordingly to deterministic rules which are integrated with random outcomes.
Predictability is directly related with uncertainty. In fact, randomness implies lack of predictability in deterministic terms. However, statistical prediction of uncertain events is still possible and useful. An interesting reading is provided by http://en.wikipedia.org/wiki/Randomness.
What is important, in my view, is to reduce (epistemic) uncertainty as much as possible while recognising the intrinsic behaviour of random processes in hydorlogy, for which uncertainty will never be eliminated. The ideal framework is the integration of stochastic and deterministic representations, therefore allowing to maximise predictability in both deterministic and statistical terms.
Predictability and uncertainty are extremely important issues in engineering and management. The recent hydrological literature presented several meaningful contributions to uncertainty assessment and modelling. On the other hand, the literature related to PUB is an excellent example of the effort to seek predictability. I think we need to move additional steps forward to set up a unified theory for uncertainty assessment and to fully integrate uncertainty modelling and hydrological modelling.
3) A theoretical scheme needs to be introduced to infer the behaviours of changing hydrological systems in time, in the presence of non-stationarity. Effective tools within this respect are “data analysis”, “comparative hydrology” and “trading space for time”. We also need improved schemes to better take advantage of modern monitoring technologies, by exploiting remotely sensed information on soil moisture, topography, land cover, biology, river network morphology and many others. Indeed, orthogonal information can represent a key for conditioning the dynamics of changing systems.
The question is: what would be the basic principles of such theoretical scheme, besides physical conservation laws and Newton laws? In fact, physical constraints are a necessary but not sufficient condition to model hydrological systems that are changing in time with many degrees of freedom. We need more organising principles to understand how watersheds and hydrological variables will evolve in the future. Ciaran Harman and Alberto Viglione mentioned the issue of “evolution” of “landscape”, “climates” and “coupled human-water systems”. This is the topic we are interested in and I like the term evolution, which implies the presence of constraints in the process. Such constraints are one of our major focuses. Ideas on their identification and formalisation in the hydrological context are more than welcome.
4) Focused activity is needed on modern technologies, to make them effectively useful. There are domains within hydrology (like flood modelling) where modern information indeed helped a lot to improve process understanding and modelling. There are other fields where progresses are obtained with a slower pace. I think there is the need to identify effective data sources for making the above emerging theoretical scheme and constraints applicable. The development of new theory should be carried out by always keeping an eye on practical applications (hydrology is a science with many implications in engineering) and data collection is of course essential to this end. Ideas are needed to identify emerging monitoring techniques that are useful for our purposes.
5) In conclusion, the theoretical scheme needs to be very general, in order to be inclusive and attractive. And, most important, should lend itself to addressing the emerging and unpostponable questions related to the interaction between hydrology and society, which also implies the effective possibility to put adaptation into practice. Indeed, socio-hydrology is emerging from the relevant role that humans are playing on the hydrological cycle and ranks high in the research interests of many countries. It is the result of the human pressures that are rapidly changing in time all over the world. Ideas are needed to assess current pressures, and to predict the future conditions in the face of sustainable development and adaptation. We need a focused brainstorming activity to emphasise the leading role that hydrology must take in environmental planning and management.
I am looking forward to a new round of comments on the above thoughts. We now need focused ideas for drafting an inclusive and coordinated science plan. I would like to remind all of you that the Task Force will meet in Vienna during EGU 2012, where a special session on the new IAHS decade (invited speakers only) is planned within the programme of the Hydrological Sciences Division. Please see http://meetingorganizer.copernicus.org/EGU2012/session/10165.
Please contact me if you are interested to attend the Task Force meeting that will be held during the EGU week.
All the best,
Alberto
Ooops! just lost all the first attempt to post a comment when my wifi link broke. I hope I can remember what I wanted to say.
First: I would like to add my thanks to Alberto for taking this important initiative which is in itself potentially inclusive if the message spreads…..
Secondly: apologies for not posting earlier – when the first call came round I thought I really had to think about this…..and then it got overtaken by other deadlines so I was very glad of the reminder.
In my mind, the question is how brave do we want to be? Yes we are dealing with changing/evolving systems. Yes, we are dealing with socio-hydrological systems? Yes, we can perceive the complexities of catchments as open, nonlinear, dynamic, anthropologically influenced, wicked systems. And we have known this for some time. There are similar problems in other areas of environmental science but, to my knowledge, there have not been great advances anywhere else either. One (sociological) response, of course, is to suggest that given the uncertainties in the science then management of wicked systems should proceed by stakeholder agreement in an adaptive way…..but as scientists we should at least have the ambition of informing the management process better in the future.
So how do we do that when we have such observational constraints? By theorising – probably not because theory for these types of systems depends on observation. That is why we are still using Darcy-Richards and Manning after over a century when both are patently inadequate at the scales for which we need to inform the management process (or even at their observational scales when taken out into the field) (and yes I know that I am also guilty of propagating their use in text books, albeit that I did so with qualifying statements). By observation – not in the near future since most of what is interesting in hydrology takes place under the ground surface where it is so difficult to obtain adequate measurements. That is why, given the additional problems of measuring precipitation inputs and stream discharges and actual evapotranspiration we cannot even close the water balance without allowing for significant uncertainties (so why do so many of our models insist on mass balance? how can that be justified in practice?).
So my suggestion for a program would be along the lines of New Observations : New Theory. A decadal time scale would allow the use of new GEOS systems like SWOT as well as a concerted effort to define the functional specification of what new observational techniques are required – ground-based as well as remote sensing – at the scales that would allow new theory to be developed for scales useful in management – such as closure schemes for REW (see my Holy Grail paper in HESS 2006). That would then (eventually) affect the way that prediction is done. The need is urgent, particularly in areas where catchments are changing rapidly, but we should not be put off by the time scales of moving from a functional spec to a feasible technical spec to the first observation. As I have suggested in the past, if we did have a method for following changes in water storage at the, say, 100m scale (rather than the 60km scale of GRACE) then hydrological theory would look quite different.
k
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Dear all,
There is a clear appeal in returning to fundamentals of observation and theory in order to answer scientific and management questions regarding complex, uncertain systems; echoing the way PUB aimed to tackle fundamental hydrological questions. I would like to add to Keith’s comment by suggesting a missing link between the ‘New Observations’ and ‘New Theory’, that is ‘New Interpretations’. By that I mean better methods to understand what current or future data sources can or can’t tell us about hydrological processes. This step is intermediate between new technology and observation techniques, and the new theories of water transport and catchment evolution mentioned by Alberto.
In some cases, our existing data can tell us more than we first thought – for example, the recent use of diagnostic signatures has shown how to get better value out of current data streams to improve our understanding, and consequently models (both model parameters and model structure) of a catchment. There are so many new/exciting data sources coming online (remote sensing data, DTS, biological and chemical tracers, to name but a few), but we are still a long way from understanding their full (joint) potential to contribute to process understanding and model building, or knowing what extra information might be needed to enable them to fulfill that potential.
In other cases, data might tell us less, or different, than we thought. Here, data uncertainty comes into play, which at its extreme can result in ‘disinformation’ (Keith’s term). More commonly, it can influence the conclusions we can justifiably draw from our data sets; and so appropriate error models, including epistemic and commensurability errors, are necessary for data interpretation.
Knowing the value of data is also key to planning future experimental campaigns or practical applications, especially under funding constraints: what data should be collected, what would it tell us? When we are trying to understand changing systems, another layer of complexity is added as we interpret data to jointly identify system response and system change amongst natural variability.
Hilary
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Dear Alberto, dear all,
I went through the comments on this blog, and I find the discussion to be exciting and very interesting. Significant international brainstorming is indeed needed if our goal is to shape a research initiative that can compete with PUB decade in terms success.
In my opinion, one of the secrets of PUB’s success lays in its very nature. Rather than promoting a new research area, or formulating a visionary issue to address, PUB channeled, and contributed to organizing previously separate international research efforts addressing one of the hydrologic problems of all times. Producing accurate hydrologic predictions on the basis of a limited amount of hydrologic information is a practical hydrologic issue that predates Hydrology as a geoscience. PUB provides international research groups with means for effective cooperation and interaction, it represents an international forum for scientists and hydrologists to confront each other and promote synergic collaborations.
I believe that also in this case it is fundamental to build the science plan on overt and shared practical problems and societal needs. I am very glad to read many comments pointing in this direction, addressing the need for “assessing current pressures” to use Alberto’s words. Therefore I perfectly agree that the new IAHS Initiative cannot dispense with the interactions between hydrology and society, meaning also improving communication between the scientific community and society (see e.g. Siva and Giuliano’s comment). It also needs to address the development of suitable technologies/procedures to profit as much as possible from the increasingly large incoming flux of remotely sensed information (e.g. Salvatore and Demetris’ comments, among others), particularly for addressing water resource management issues in emerging and developing countries (e.g., Viglione et al. comment).
Most importantly, in my view, the initiative should not fall into the pitfall of making predictions of environmental change or uncertainty assessment the ultimate goal of our research efforts. These are indeed important topics, but only to the point that they are useful for identifying the optimal (i.e., most feasible, accessible, sustainable, etc.) solution to the water-problem in the current scenario. Prediction of change should not be the end, it should rather be the means by which we assess the robustness and adaptation capabilities (i.e. resilience) of hypothesized solutions to today’s water-problems.
Let’s join our forces to bring this big picture into focus.
Cheers,
Atti
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Some thoughts on future directions for hydrologic research
Earth scientists have long recognized the strong controls climate exerts on landforms and soil development (Jenny, 1941), ecosystem composition and global biome distribution (Whittaker, 1962), and river basin hydrological partitioning (Budyko, 1974). Hydrologists like Milly and Zhang have investigated the role of climate seasonality, ecosystem composition (e.g. grassland vs. forests) and soil storage capacity (relative to average storm size) to explain deviations of long-term river basin water balance from Budyko’s hypothesis (E/P=φ(EP/P); E: evaporation, P: precipitation, EP: potential evaporation). Yet, much less attention has been paid to understanding the interactions between climate, vegetation and soils and their co-evolution within catchments. Such interactions and co-evolution is blatantly visible when traveling along sharp climate gradients, for instance when moving up in elevation along mountain highways. A beautiful example is the Santa Catalina Mountains near Tucson, Arizona. The Catalina Highway connects the Sonoran desert valley floor with mixed conifer landscapes near the mountaintop, and while traveling the 1-hour trip one crosses 6 different ecosystems. These ecosystems coincide with clear gradients in soil development (soil depth, coarse fraction, % clay, etc.) and correspond with specific climate conditions. It stands to reason that catchments located along this climate gradient will exhibit predictable patterns of hydrological partitioning. At a given elevation, soil and vegetation properties are further controlled by aspect (the amount of solar radiation received at the land surface) and lithology. In the small experimental catchment that I work in (Marshall Gulch near Mt. Lemmon, the highest peak in the mountain range) there is a sharp transition from schist to granite bedrock, and differences in chemical weathering rates of the main primary minerals have led to clear differences in soil development and ecosystem composition. One can easily observe the geological transition by looking at the trees; once you have crossed into the granite base, the Rocky Mountain Maple trees (Acer glabrum) have been replaced by White Fir (Abies concolo), reflecting the differences in water balance between schist and granite soils. Marshall Gulch has a W-E orientation, and thus the main hillslopes are S-N oriented. South facing hillslopes are steep and covered with thin soils, while North facing hillslopes are less steep and have thicker soils. The forest fire of 2003 (the Aspen fire as it is called) burned most of the trees on the S facing slopes in Marshall Gulch but has left most trees on N facing slopes intact.
So, the amount of water and energy a given place on Earth receives determines the combination of vegetation, landform and soil, and the level of development depends on lithology (the initial condition) and time. This co-evolution of landscape properties will in turn affect how water and energy is partitioned at catchment scales. Understanding this interplay in the context of catchment hydrologic response, to me, is key to advance scientific hydrology. If we can understand how catchments have developed at a given location and how that evolution can help explain observed hydrologic response (e.g. storage dynamics, water balance partitioning) we will be able to provide answers to societal important questions related to natural or man-made changes in the environment. We won’t know where we go if we don’t understand where we come from and why we are where we are.
Moreover, understanding the interplay between climate, vegetation, soil and hydrological response will guide us to construct better models and will hopefully help us to reduce prediction uncertainties. Our current hydrologic models are constraint by conservation laws (mass, momentum, energy) but are not restricted when it comes to assigning soil and vegetation parameterizations. This doesn’t make much sense, come to think of it. Yes, we do try to use as much as possible geographic information systems to inform land parameterizations (topography, land use), but important processes in the subsurface are usually parameterized using unconstrained optimization (unconstrained in the sense that we usually do not add restrictions to specific soil-vegetation-landform parameter combinations). This is not a critique but an observation that stems from the fact that we simply don’t know how to formulate these landscape constraints, because we never have asked that question.
So, my suggestion for the next decade of international scientific hydrology is to embrace the notion of catchment co-evolution in an effort to synthesize the many data sets and theoretical models that have been developed in our and other Earth science disciplines, and to develop new hydrologic theory. Pedologists and geomorphologists can predict, to some degree, how soil properties are distributed across a landscape, while ecologists understand how vegetation composition changes along gradients. We should be able to take advantage of these insights that will help us understand how catchments may respond to environmental change.
Our research agenda could be organized around different lines of attack:
1. Encourage experimental design that allows addressing questions concerning landform-soil-vegetation characteristics within and across catchments. When hydrologists organize fieldwork they usually ask the question: “Lets find out how this catchment works”. That has led to a treasure of placed-based research and understanding, but because of the way the question was formulated and the research was set-up, it is very difficult to generalize beyond that given place. One counter example of this is the work related to paired catchment studies. These studies were set-up with a very focused question: “How does catchment vegetation (and planned/observed changes) affect hydrological partitioning”. Because the question was very focused this research led to some important consensus science. We can make similar progress if we have common questions that go beyond a given place. This will require careful experimental design and common goals across research teams.
2. Recognize that hydrologic response is more than the hydrograph. PUB was a huge success and its main focus was to reduce uncertainty in predicting hydrographic response of the landscape. But we can learn so much from trying to understand how catchments process water and carbon, nutrients, and sediments, and how biological processes affect these stores and fluxes. There is an active community gathered around catchment science (e.g. the standing Gordon conference on Catchment Science) and IAHS can play a pivotal role in reaching out to this community and propose addressing common questions. It should matter as much to a catchment hydrologist as to a biogeochemist why certain space-time dynamics are observed in nutrient cycling, because it will reveal much about internal functioning and landform-soil-vegetation interactions. After all, the most significant breakthroughs in catchment hydrology came from analyzing the chemical response of catchments, discovering that most water leaving the catchment is pre-event water and that evacuation of inert tracers show scaling behavior related to subsurface heterogeneity.
3. Stimulate comparative hydrology across natural and man-made gradients. One way to synthesize knowledge is by comparing and contrasting existing data, and to try to find patterns that can help formulate hypotheses related to landform-soil-vegetation interactions. A good example of such an approach is the Hydrologic Synthesis project led by Siva.
4. Develop the hydrologic narrative. Too much of our efforts are focused on predictions (most of us are engineers, after all, including me), while we have neglected coming up with explanations of what we observe. Why does a catchment partition water and energy the way it does? Can we read the landscape in order to find that narrative, similar to how geologist and geomorphologists read the landscape to explain how it came about? Focusing on the narrative will enable synthesis across locations and will stimulate critical thinking. This is a perfect community effort and IAHS can play an important role in stimulating this scientific approach.
5. Take advantage of advanced remote sensing technology. Data sets from LiDAR observations, for instance, hold a wealth of information about the interactions and co-evolution of landforms, soils and vegetation, and should be mined to reveal patterns across lithologic and climate gradients. These patterns, in turn, can guide model development (both in terms of new processes as well as in parameterization of existing models). Behavioral models of catchments across these gradients can then be used to test specific hypotheses. This will allow, to some degree, exploring catchment functioning of the subsurface, which is notoriously hard to observe.
6. Develop models to test hypothesis, not to make predictions. If it works out, improved predictions will be a pleasant side effect of this effort. TOPMODEL and GIUH were brilliant breakthroughs because they allowed testing of hypotheses related to the geomorphologic structure of hydrologic response at the catchment scale. Similar success is possible if we construct models that account for observed spatial patterns in soil properties and vegetation composition related to the geomorphologic structure of the landscape.
In conclusion, I have tried to bring together several ideas that have been proposed on this site into a consistent research framework that can guide us into the next decade. This is far from complete and represents my limited understanding of hydrology, but I hope some of you will find it of enough interest to further the debate.
Peter Troch
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Dear Alberto,
I wish to thank and congratulate you for provoking such a high level of discussion and for your illuminating posts. I particularly congratulate you for NOT eliminating “uncertainty”(1)–at least so far. Eliminating uncertainty in modelling is infeasible, but NOT eliminating the term and the notion of “uncertainty” in a discussion about the future of hydrology seems to be hard too. My fear is that “uncertainty” is going to be “eliminated” or “radically reduced” in the final document of the new Science Initiative for the coming decade. That will be a pity, though, because:
– if we try to improve our understanding, then understanding uncertainty should be one of our first priorities;
– if we focus on prediction, it would be optimal to study its twin, that is, uncertainty–there cannot be hydrological prediction without uncertainty;
– if we accept the notion of change and try to study it, we should get reconciled with uncertainty as well–when envisaging the future, there is no change without uncertainty;
– if we try to view the links of hydrology with the society, I think one of the most important services of the hydrological community to the society is its capacity to illustrate how we can live and make progress under uncertainty.
I wish all of us be in good health in 2022 and contribute to the discussion about the science directions for the following decade. Perhaps we will all have a feeling of déjà vu then(2). I feel I can safely predict that those who view uncertainty as an enemy that inhibits understanding will not be able to celebrate a triumph against the enemy.
Demetris
PS. (1) I and my co-authors have discussed the zeal to eliminate uncertainty, which had also affected the initial aspirations for PUB, in our paper “Climate, hydrology, energy, water: recognizing uncertainty and seeking sustainability” (http://dx.doi.org/10.5194/hess-13-247-2009). This triggered interesting comments (http://www.hydrol-earth-syst-sci-discuss.net/5/2927/2008/hessd-5-2927-2008-discussion.html), suggestive of how the meaning of uncertainty and randomness is (mis)understood within the hydrological community.
(2) Here I borrowed a phrase from a good comment by Sivapalan on the first blog post.
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I am concerned about the emphasis, in discussion of the new IAHS science initiative, on “socio-hydrology”, defined as the interaction between hydrology and society, and would like to express a dissenting view. “Society” is a very nebulous term; there is no single society, and there is no common hydrological theme connecting the water requirements of, say, an urban society living in a Brazilian favela, an agricultural society of Bangladeshi rice farmers, a society of Chinese factory-workers producing components for tablet computers, and a society of citrus producers in Florida. All will have different water needs and expectations, and all will respond differently to water shortage or excess. If we are not careful, hydrology will become an appendage to social engineering, and we shall be in danger of losing sight of what hydrological science should be about. IAHS is the International Association of Hydrological Sciences (note the word “Sciences”), and it is developments in the science that should be principally addressed.
One definition of hydrology is that it is the study of the land phase of the water cycle. Expressed in another way, it is the study of what becomes of precipitation after it has fallen, and how it makes its return journey to the oceans or to the atmosphere – the pathways that are followed, and the times taken to reach these destinations. Yet it seems to me that, even after well over half a century of hydrological endeavour, we still do not know very much about such pathways and the times taken for water to travel through them. As one example, many (all?) hydrological models represent “baseflow” as the output from a series of reservoirs, linear or non-linear, but these conceptual reservoirs have no physical existence. As a concept, they satisfy the positivist view of hydrological science, in which the role of science is seen as being the reconciliation of observational data. For the positivist, if one can make predictions that accurately account for what has been measured, the task is done; ontological questions (about what is really there) are an irrelevant luxury and can be discarded. I should prefer to see an IAHS initiative that is more realist and less positivist: realist in the sense that it is concerned with what the physical world is actually like and how water behaves in it. Given a unit of precipitation reaching the earth’s surface at a given time, what pathways do its molecules follow in their return journey to the ocean or atmosphere? What happens in transit: how continuous is the journey, and is it interrupted by periods of temporary (or indeed longer-term) inactivity? What happens to water during such periods?
To answer such questions will require much greater emphasis on basic science, in my view, to establish how water pathways can be traced through soil, plant and aquifer, and to determine the physical and chemical changes of water as it passes through them. In this, hydrologists could perhaps learn from the clever tracing techniques now used by biologists to track what is happening at the cellular level; and, as been mentioned, modern technologies offer unprecedented opportunities for hydrological scientists.
The study of how to detect change in hydrological behaviour has also been mentioned in a number of contributions to the discussion, and this too requires much thought about how hydrological scientists can best contribute. Here, I think we should not be looking for statistical trends in river flows or environmental variables, which are complicated by land-use changes, changes in measurement methods and instrumentation, missing data, and other difficulties. Climate change, if and when it occurs, will be driven by physical processes in the atmosphere leading to changes in precipitation amount, its spatial distribution, and the factors that control evaporation. More research into the atmospheric processes acting near the earth’s surface, and how they interact with surface topography, is – in my view – the way forward for hydrological scientists, with less emphasis on the fine-tuning of rainfall-runoff models.
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Dear all,
Reading through these interesting discussions, there appears to be a consensus about the need to advance hydrological process understanding and modeling approaches (incl uncertainties) under changing (non-stationary) conditions. This is not surprising since changing climate conditions and the increasing pressures from land use activities and water requirements are causing real problems for societies and ecosystems, as also discussed at the World Forum meeting this week
(http://www.youtube.com/watch?v=aGuDJDudCO0 ), and at the same time it is challenging the premises of operational and scientific hydrological modeling approaches.
I agree that there is a need for basic scientific and applied research to develop new theories and advance the capabilities of models to forecast hydrological responses during conditions of changing climate forcing, human pressures and landscape structures, and not the least to predict the (hydrological) consequences (and uncertainties) of climate change and decision making processes at the various spatial scales where people and ecosystems are affected.
Because humans are actively exploiting and modifying hydrological systems, it should be necessary to represent societal development (ie land use, urban structures, water supply, waste water) and stakeholder activities (ie. irrigation, water abstraction, damming) which are influencing the properties and state of the land surfaces and landscapes hosting the hydrological processes. In order to represent human activities, understanding of natural (“reference”) hydrological processes and the interaction with atmospheric processes is clearly also necessary. Therefore research in both natural and modified hydrological systems under environmental change should be encouraged.
It is generally agreed that the new IAHS scientific initiative should be inclusive and multidisciplinary and thus support a large variety of theoretical, empirical (field-based) and modeling approaches, as does the PUB initiative. In addition to using new data and analytical techniques for developing new hydrological theories, one way of addressing change could be to clearly encourage further research and predictions in contrasting catchments. In order to understand the hydrological processes of two or more contrasting catchments, historical data, new analytical approaches, process-oriented research and comparative hydrological studies would be essential, and such a research framework might work to advance theoretical, empirical and model-based representations of the roles of climate, humans, land surfaces and landscape structures in catchment hydrology. Hydrological processes in populated/modified catchments could be studied in relation to natural “reference” catchments with similar geological settings, or hydrological responses in different climate zones could be systematically studied using hydrological and atmospheric data. There appears to be many relevant research questions related to comparative studies of two or multiple (natural or modified) contrasting catchments which could be further elaborated to target objectives aimed at improving our understanding of hydrological systems and their responses to climate gradients/trends, various land use development rates, landscape structures or water abstraction histories.
Eva Boegh
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Dear Eva and others,
I very much agree with the comment above about learning opportunities from research and predictions in contrasting catchments. Our underlying motivation in catchment studies is very often to try to describe general ‘laws’ which might be applied in many places. To achieve that it’s important to understand how system behaviour and observations differ between catchments.
Our current opportunity is to undertake those comparative studies not just in two or three catchments which we might be familiar with, but using country- or world-wide data sets which are brought together by the hydrological and wider communities. Here I’m thinking of efforts such as the UK-based Environmental Virtual Observatory (http://www.evo-uk.org), the Global Runoff Data Centre (http://grdc.bafg.de), or the CUAHSI Hydrologic Information System (http://his.cuahsi.org/).
These types of shared data sets are and will be a great resource for hydrologists like me trying to make the link between observations, process descriptions and appropriate simulation models. A key point will be to ensure that there is sufficient allowance for flexibility of data types and meta-data storage alongside the data set. This will enable the new and creative data interpretation techniques (as per my previous comment) which are needed to drive forward our understanding of the catchment system, but may not have been thought of when the data was originally stored. It’s equally important to store information on the data uncertainty and methods used to collect the data, to help remote users understand the value and limits of the measurements and gain some of the insights of the field hydrologist.
Cheers,
Hilary
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Dear All,
it is comforting to see how alive is this discussion on the expectations for the future of hydrological sciences (and how many different ideas have been presented, thus showing what a multicolour community we are…).
Of course I can’t but agree that gaining a better understanding of the physical nature of the processes underlying the formation of the ‘hydrograph’ is very important from a scientific point of view: most of us are researchers, but, as Peter underlines, many of us are engineers too – and this is not a downside! -, and we should never forget that one of the most important practical issues that hydrologists should address is improving predictability from a technical point view (unlike Peter, I believe that the effort focused on predictions is never enough…).
Obtaining reliable and practically serviceable predictions is crucial for a variety of human activities aimed at improving the life of our society (or better, societies, following Robin’s comment), from flood prevention and forecasting to drought mitigation measures. Hydrology should be strictly connected with the other civil and environmental engineering subjects: our students, once outside the University, will mainly deal with the problem of consistently estimate design variables and therefore predictability, coupled with uncertainty assessment, is a relevant issue.
Improving the understanding and the detailed modelling of the physical processes will certainly, in prospective, improve predictability, but I think that a fundamental contribution must come from the full exploitation of the available data: data may be seen a tool for describing and at the same synthesizing the main features of a complex reality like the hydrological world and may help us to understand it better. I believe that the good predictions that may be obtained with simple black-box, or ‘data-driven’, models, are a proof of the meaningfulness of the information – about the certainly complex catchment processes – that is embedded in the available observations, information that we must be able to extract and to exploit to the full.
I strongly support, therefore, the stress put by Salvatore, Alberto and Hilary on the crucial role of data analysis and in particular of modern monitoring technologies and the importance of understanding the value and the limitations of what data can tell us (and I fully agree with all Hilary wrote on March 16th…).
Elena
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Dear all,
a new IAHS initiative would represent a fantastic opportunity for our community. There are several topics that still remain long-standing issues.
As Peter Troch emphasized, understanding the interdependence of the soil-vegetation-climate and hydrologic cycle remains a fundamental problem toward accurately predicting the annual/interannual surface hydrologic cycle. This is especially important in the context of climate change and human influence on the landscape and ecosystems. So as such it is intimately coupled to the human response/forcing. One of our aims should be to get predictive power in the context of non-stationarity (Milly 2008). This non-stationary will impact the surface hydrologic cycle on a diversity of time scales (intra/interannual variability, decadal changes and alteration…). One of the main challenges is that this understanding encompasses many fields (geomorphology, pedology, ecology, atmospheric science, surface and groundwater hdyrology). As such it requires a combined effort among different groups of people, sharing different languages. Yet combining our effort (and possible merging some of the curriculum to train the new generation of hydrologists) might lead to new discoveries at the interface of those fields and toward the same goal.
Toward that objective, I believe we could learn from the climate community. They have had a very well defined objective for the last few decades, improving our prediction and understanding of climate change. They have really worked as a group toward that goal. They have for instance run many model intercomparisons (along with comparisons with observations) in order to evaluate the deficiency of their physics representation. This has led to fundamental progress in the parameterizations of climate models (e.g. cloud representation, convection,…). A good example is the intercomparison of boundary layer and convection schemes to assess the quality of their representation of observed cloud patterns and transition over the Pacific (CGILS). We could have the same strategy for catchment hydrology: define typical catchments along a climatic gradient (which would be very well instrumented) and have several intercomparison studies of the surface hydrologic, using both coupled and uncoupled version. Among the many problems that we currently have in model representation we could evaluate for instance: heterogeneity impact on water transport, vegetation organization across space (time and space), atmospheric coupling and how it impacts evapotranspiration, remote sensing…
Pierre
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Firstly I would like to congratulate the group on the initiative of the IAHS. It is a great pleasure to participate in this discussion group and also be able to express our opinion. In the last months we have talked with some scientists involved with issues related to the impact of agriculture on water resources and the problems associated with sediment yield. A major problem we have been facing is the tendency of the advance and intensification of agriculture on fragile areas.
In our opinion, the central point in the hydrological science has to contribute is how to manage the progress of economic activities considering the fragility of natural systems and your functionality, enabling social development.
We have selected some of the major scientific concerns:
• In Brazil and other countries in South America there are still large areas with insufficient number of data (solid and liquid discharges) that allow to understand the dynamics of important systems. Strategies to improve the monitoring network is essential.
• The ability of prediction (quantify) the impact of the advance of agricultural activities due to the relaxation of the legal requirements is a key point for the preservation and management of important environments, both at regional and local levels.
• Generation of information and tools capable of accounting for the economic impact of the actions related to agricultural, industrial andurban activities on water resources.
• Actions designed for urban planning aimed at water resources management and disaster reduction.
Again, I would like to thank you and to say that we will pay attention to the discussions for future participation.
Jean Minella
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Dear all,
it was very interesting to read the comments and I really appreciate the possibility to contribute to this initiative. Below I add some ideas and suggestions that are the result of my experience. I hope the comments could be useful to further debate.
In the last decades an increasing number of studies have focused on the uncertainty of model prediction. In this contest I think it is not necessary to cite any work but I want just to underline the effort given by the scientific community to try to cover all the sources of uncertainty e.g. parameters, input and model structure. I hope this goal will not lose his importance as more and more we need studies of this type if we want to understand the applicability of the models in a real decision support system.
However, as suggested by Alberto Montanari, I want to underline that for the scientific community the natural step further after the uncertainty analysis should be how to reduce this uncertainty. This goal is also not completely new and some interesting works are presented in literature but in my opinion this aspect is still limited and no clear guidelines are presented. In this way it raises a need of a more clear vision.
I would suggest that the development and the comparison of quantitative methods to rank all the sources of uncertainty considered in the assessment of a model should be a great and important challenge for the future. This information can be in fact useful to assess how far the prediction uncertainty can be reduced by reducing the uncertainty of a particular source.
In conclusion, I agree that uncertainty assessment is not the ultimate goal of our research efforts but I would encourage initiative and studies to define in a goal oriented approach how to reduce this uncertainty for future application of the model.
Best regards,
Gabriele Baroni
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Dear Alberto
thanks for your first summary of the first set of discussions.
I agree with many of the themes that emerged from it, especially about the major importance of ground based data.
About this topic I think personnaly that one real challenge for hydrology in the future would be “Scale transfer in Hydrology”.
I see for instance 3 subtopics:
- the first is related to a question : “How to use local knowledge for global purposes” in large river basins ? This meet most often a social demand, when you have to give “global certainties” and not “local uncertainties” to national services which try to dimension a future project.
Methodlogies and tools are not always ready to answer to this question. Much experiments must take place for instance to select the variables which will better represent a specific phenomena, considering constraints like spatial coverage, repetivity, length of the time series, robustness, of existing data series.
- the first type of “global” data are linked to demography and agricultural data, at the basin scale. These data prove very useful to calibrate satellite derived NDVI for instance, and to create relationships available for periods before the first satellite images. Thus using satellite data, especially mid-high and medium resolution data which cover large areas, are particularly well fitted for large river studies, especially when they cover a long time series. Among this topic, a sub topic seems very important to me, it is “how to improve our knowledge of actual/real evaporation ?” It is most often what limits the performances of our hydrological modelling.
- the third topic would be according to me “how to better interact with climate modellers” as far as hydrological modelling is concerned. We must be able to propose to climate modellers surface schemes for GCMs or RCMs that take into account as much as possible the local knowledge of hydrologist. For instance, I do not think that any GCM or RCM in Africa integrates the fact that runoff has increased in Sahel since 40 years. For sure the surface schemes just produce less runoff with less rain, and what happens is exactly the reverse, due tho changes in land use. Thus the amount of water available for local energy fluxes has decreased since.
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Dear all,
I agree with the past comments on the need for increased efforts in the evaluation of models. This should help better understanding their strengths and weaknesses and ultimately help improving their predictive capacity as well as their explanatory depth.
Here are a few suggestions that could be considered:
- the development of improved methodologies to test models, especially in changing conditions. Limited work has been done so far on this issue, but there is a strong need for devising more demanding testing schemes that could contribute to a more in-depth evaluation of models (e.g. how well do they manage to extrapolate in non-stationary conditions?). Various aspects of modelling could be further investigated and tested, especially in terms of spatial and temporal scales. We should also reinforce the reflexion on evaluation criteria, to build criteria in better agreement with expert knowledge for various applications.
- the development of databases gathering large numbers of case studies, that could be made available to the whole community. The scientific literature abounds in case studies on a single site, with conclusions that are difficult to transpose elsewhere. We need to get more general and statistically robust conclusions. And we could often learn much more in confronting results in various sites, possibly under contrasted conditions. Specific data sets could be set-up, for example data sets with catchments that experienced strong long term climate variability and/or changes in land-use of similar type (e.g. evolution of forest cover or urbanization). Detailed data sets from experimental catchments, as well as national measurement networks should be of helpf for that.
- contributing further to comparative experiments in line with past initiatives (e.g. DMIP, WMO comparisons, etc.) that attempted to put models in harmonized testing frameworks to make evaluation results more comparable. These comparison initiatives should not be restricted to hydrological models but also to various methodologies that are part of the modelling process (e.g. uncertainty estimation). More generally using benchmarks in model evaluations should also be encouraged.
- put more efforts in the analysis of model failures: when applying models on large data sets and/or in difficult testing conditions, there are always catchments or conditions where the model fails. These cases are generally challenging and helpful to find new ways of model improvement. This is even truer in changing conditions.
Regards,
Charles Perrin
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Dear Alberto and IAHS Family，
It is a great idea to have this platform available to have a warmer and warmer discussion about next hydrological decade. I like to read the idea sparks so far from all the hydrologists, some I am so farmilar to and respect and some with new faces and fresh air into the family.
I do not have a better idea out of discussion-stream so far. May I just raise a suggestion to give a minor revision to the name of the next Hydrological Decade？i.e. using “Hydrology in an Uncertain Change” (HUC) instead of “ Hydrology under Changed Conditions” （HUCC）as the name of new initiative of the IAHS.
They look similar. However this “U” is better than that “U”.
Living in the water-related environment, which is changing so quickly nowadays, most of us (if not all) will not disagree that changes turn so important for hydrological research.
For years hydrologists have dealt with many changes to, of and by hydrology.
However, to make the next IAHS initiative more practical and more exciting, we can not catch all kinds of changes existing. The name of “The Hydrology under Changed Conditions” may be too abroad.
So far what has been left unsolved, yet extremely wanted hydrologists to find a further solution，is the uncertain change. PUB has generated great products on uncertainty research. Aiming in an uncertain change will make better use of results of last Hydrological Decade and make the flow of Hydrological Decades running through smoothly.
I believe the minor change from “The Hydrology under Changed Conditions” to “Hydrology in an Uncertain Chang” will bring a strong difference as a research flag in next decade of Hydrology.
Kind regards
Suxia Liu
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Dear All,
I would like to thank Alberto for initiating this blog and chairing this open discussion.
I am just back from EGU and just finished reading the comments on this blog and I got the feeling that our discussion on future steps in hydrology has become a very exciting intellectual exercise, but (you should expect some BUTS at this point…) has got too much of a “philosophical drift”.
I am afraid we are moving more and more away from the actual needs of the engineering/hydrological applications.
Something I feel is missing in all comments is what I consider the key question: what does the “real (engineering/technical) world” need from scientists? Are we doing Science for Science? Shouldn’t we spur the participation of representatives of engineering agencies, stakeholders, civil protection agencies into this very useful exchange of opinions?
In my limited experience, I have noticed that some of the future steps we are proposing for our research in hydrology is what many technicians actually do in their day-to-day practice (and I find it particularly true in data scarce areas and developing countries): they look at the past, they go on site to look at the landscape, local characteristic of the basin and compare across space.
My point is that we should not loose contact with real world and how real world digests, interprets and makes use of the outcomes of our research.
I believe that one of the gaps we should try to bridge between science and technics is uncertainty. How do we recognize, assess, quantify, transfer, accept uncertainty? How do we use our (uncertain) models for real world applications.
I also believe that the civil population is well aware that we are living in a changing world. I read some comments mentioning that we should look at changing condition. At least since the industrial revolution changes have been fast, visible and trackable. We are not finding out today that our world is non-stationary.
So, my suggestion is to look at assessing uncertainty in future changes and explore how to take that into account in water resources planning and management. As an example, many of the hydraulic structures in service are aging and they are approaching the end of their life-time and are nowadays either underdesigned for the current (and future?!) needs or are poorly maintained: how can we assess and reduce uncertainty in future water demand, water use, design variables to minimize the problems we are facing today?
Luigia
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Dear All
At this stage, the discussion seems to be to strongly evolving around methods that should be developed in the new science initiative, list of tools to be used, questions and problems to be addressed. A lot of ingredients without any plans for who to invite to the diner
The very interesting inputs to the discussion will be of great help to fill in all details of the science initiative but I think it is important to forget for a while the scientific inductive pathway and propose first an overarching theme from which we can deduce all the activities that should be implemented. A theme that sounds attractive to specialists and stakeholders, which seems to be specific but which leaves enough room for interpretation to become inclusive. Ok, this is difficult, but let’s be creative and propose names / titles!
My contribution to this effort is that this title should definitively include the word “FOR”, i.e. the title should tell everyone why and for whom we are doing research (thus: not Prediction of changing systems or Prediction under change but Prediction for an evolving society).
I am convinced that finding an appealing title with which many people can identify will, at this stage, help to advance the discussion.
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I would like to add something: I am of course aware that some comments (Siva, Alberto) suggested to wait for the name of the new initiative to fall out of the discussion (Siva, 29.1.) : “Once the nature of activities is decided, the naming of the initiative may naturally fall out of this”). I think we have reached a point where synthesis is required and I am convinced that discussing potential names and title keywords can be a way forward. Do we e.g. want to have the key word “prediction” or “understanding”? “Socio-xx” or not?”, “change” or “co-evolution”?
Bettina
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