As a follow-up to my previous post, see also here, I'd like to share some additional reflections on the experience of doing hydrology in academia. I've attempted to classify different types of researchers, and below, you'll find the second part of this classification.
There are those who hypothesize relationships, laws, models. In this context, statistical analysis plays a key role, even in its modern algorithmic forms, producing various models that uncover causal relationships and correlations. Possessing good mathematics skills avoid to be trivial and adapt your solutions to your ability (if you have a hammer, you tend to see any problem like a nail). It is not an infrequent attitude in Hydrologist being impatient to get number and result as if the mathematics were a commodity. Any problem needs its mathematics. Opposite of the previous attitude, someone is in love with mathematistry, and try to impress people with unrequired complexity or concepts. Maybe they gain some paper on major journal but that will rarely be cited. Where the proper use of mathematics stands, is also the good science that should be worthwhile to pursue.
Example of mathematics used in hydrology is the solution of partial differential equations like de Saint-Venant equation, Richards equation and groundwater equations with the additions of the Naviers-Stokes equations when transport in atmosphere is pursued. To these equations and their direct simplification, the heat transfer equation and various diffusion-like equation were intended to be the last word when dealing with the energy budget and various transport phenomena.
Their use was seen as a needed progress with respect to the use of empirical formula and supported in the famous blueprint by Freeze and Harlan, that however found several criticism and several defenders*.
While the previous description of the physics of the processes was though as superior to empirical equation (mostly simple regressions) or closed formulas of pre-digital era, still it has often claimed that not the whole information contained in those equations was relevant to produce macroscopic estimator of the water budget (often just the discharge) and only a few degree of freedom survive to the dynamics and the coarse graining that works in catchments. However, not consistent proof was so far produced that could lead to the right simplification of equations or methods. [[Only the Witthaker / Gray integration methods, that have found just few factual believers. ]]
At the catchment scale, ordinary differential equations (ODEs) have remained the dominant mathematical framework. The prevailing idea is that a set of ODEs, potentially organized within a graph of interactions, can effectively capture most of a catchment's hydrological dynamics. However, no formal proof has yet been established to confirm that this state-of-the-art approach is universally consistent—its widespread acceptance is largely based on empirical success. What many don't realize is that the ODE approach can also be viewed as an integral part of the so-called Instantaneous Unit Hydrograph (IUH) theories. These theories have recently experienced a resurgence, partly due to their intersection with new measurement techniques involving stable isotopes.
I wrote somewhere:
Aristotile had it all wrong.
Dalton, Horton, Sherman and Leopold plaid the starting gong.
Eagleson, Rodriguez-Iturbe went for a grand theory, in which they believe.
Gideon and Ignacio (Vujica teachs) dated with randomness.
Richards, Richardson, Harlan and Freeze insisted on using PDEs.
Horton said the the runoff is infiltration excess,
Dunne said that it is saturation excess,
Hewlett and Hibbert said that overland flow necessary is not
Tracers research screwed all it up.
Darcy and Buckingham it is all matter of gradients they thoughts.
Beven and Germann set up a mountain of doubts.
And many, I forgot, I do not know
Now we do not really know what we know,
except that we know more than before,
better data we have,
satellites see it all (but what you see you do not believe).
Modelers give numbers, without caring
machine learning thinks it can do all without understanding
and because we did not had it when we thought,
they probably sing the right song
If you address the existing gaps in this theoretical framework, your work would be well-suited for publication. Similarly, if you introduce novel approaches in the application of PDEs, develop new models that combine ODEs and PDEs, discover innovative methods for parameter estimation, or invent new solvers, a new implementation of a known theory, previously neglected, your contributions would be highly valued and welcomed for publication.If you're truly ambitious, you might consider introducing a new branch of mathematics for describing phenomena—much like fractals, fuzzy logic, and other methods did about thirty years ago. Doing so could earn you a lasting place in the literature. Additionally, there's still significant potential in established fields like information theory and causal inference, which could be further explored and systematically applied, offering you the opportunity to gain recognition and influence.
The latest trend is undoubtedly centered around machine learning techniques, which have proven highly effective at replicating the behavior of hydrological systems—often without fully understanding the underlying mechanisms. Today, the field of machine learning is ripe for exploration, and there's ample opportunity to publish in this area due to its resurgence in popularity. However, papers that merely imitate existing work are unlikely to have lasting impact or relevance.
In reality, many of the approaches and models that continue to find their way into publications remain, even today, remarkably simplistic. I admit, I have been guilty of this myself. Examples include degree-day models for SWE estimation, outdated infiltration formulas, empirical methods for potential evapotranspiration, and basic time-based formulas for peak flows. These methods are often said to work, but only after episodic parameter calibrations and inadequate, narrow verifications. Wolfgang Pauli might have deemed these methods as "not even wrong," implying that they lack sufficient depth even to be considered incorrect. Dante might have consigned such papers to the ranks of the "ignavi," those souls unworthy of a place even in the circles of Hell.
If you manage to replace these obsolete methods with more robust alternatives, your work is certainly publishable.
Many professionals have built their careers by advancing technical aspects related to models and theories, such as uncertainty assessment, parameter calibration, and data assimilation. This is undoubtedly a viable path for a researcher, one that can lead to significant recognition. Moreover, there are several promising areas within stochastic hydrology, including groundwater studies, time series analysis, and forecasting. Although these areas may not align perfectly with my current focus, they represent fertile ground for research and development, and have recently seen a resurgence of interest.
*A NOTE: The use of PDEs that actually were derived from the foundations od physics, let the door open to the fact that some aspect were simplified and some parameters of the equation have only a statistical significance. For instance in Richards equation, the soil water retention curves that play a fundamental role are equilibrium relationship between the water content and the chemical potential of water in soil that is realized when the system has the time to relax in order to the smallest capillaries fill first and empties last. There is a famous sequence of papers by Keith Beven treating some of this topics that you should recover (but not necessarily agree upon). So the supposed fundamental PDEs are sometimes not that fundamental and often depends on parameters that have the faint light of some slippery statistical significance.
